Review Reports - Comparison of the Effectiveness of the DNIPRO Gen 2 and SICH Tourniquets Versus the CAT Gen 7 and SOFTT-W Gen 4 Tourniquets

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Dear authors, I thank you for submitting this manuscript and for the opportunity to review it. I know that in low-resource settings, CoTCCC-recommended tourniquets are not always available, and I appreciate this study, as it will hopefully start bridging the gap between what is available on the ground in Ukraine and evidence-based management of bleeding control.

Please address the below points:

Abstract

Line 26 – I could not find a SITCH tourniquet. I believe that you are referring to the SICH tourniquet, made by SICH Medical LLC. If it is indeed SICH, please update the whole submission.

Line 38 – Please report the full term (e.g., Median) before the abbreviation in the text. Also, the usual abbreviations for Median are Mdn or Med. I have not seen Me before.

Line 39 – I believe that the conclusion “These findings indicate that Ukrainian-manufactured tourniquets may serve as effective hemorrhage control tools in prehospital and battlefield settings” is too strong for a preclinical comparative study. I would rephrase it to indicate that the Ukrainian tourniquets might have similar performance compared to the CoTCCC-recommended tourniquets.

Introduction

Line 77 – Achieving “arterial” occlusion.

Line 77 – I would change pain tolerance to pain during application, as you are not measuring pain tolerance in this study.

Line 84–85 – I do not think that you used a standardized user-based model. We do not know what tourniquet was used first, where it was applied (mid-thigh, proximal thigh, forearm, proximal arm, etc.), whether it was applied over clothes, etc.

Methods

Overall, I would always follow the same order when you explain your outcomes of interest in the Methods and Results sections. First arterial occlusion rate, then speed, then pain, then ease of use. You can choose the order, but please be consistent throughout the manuscript. Some abbreviations are introduced multiple times in the manuscript; please ensure that they are introduced only once in the abstract and once in the manuscript.

Line 100 – Please move all results (e.g., participant sex, percentage of physicians) to the Results section. You can also define and add:

The average length of experience of the participants.

What role the non-physicians had (medic, nurse, etc.).

Line 103 – Please define “medical education” and “clinical experience,” as this affects the generalizability of your findings.

Line 107 – I appreciate that you took the time to describe all tourniquet types; please add an appropriate industry reference for all tourniquet types, including the headquarters of where they are produced.

Line 117 – “are” intended.

Line 163 – Was the order of the tourniquets used and the limb on which the tourniquet was used decided randomly? For example, if all participants practiced first with the CAT and then moved to another type, there could be a learning bias affecting the time of application. Additionally, what kind of experience did the participants have, and what tourniquets do they use in their clinical practice? If they all have experience with just one of the tourniquets tested, this may introduce bias and should be addressed in the limitations.

Line 167 – Please specify exactly where the tourniquet was applied anatomically (high and tight vs mid-limb, etc.). Please specify if the tourniquet was applied on bare skin or over a uniform.

Line 172 – Please place the reference for the Butterfly device.

Line 174 – Please specify where you measured the flow (which artery and where) and for how long. Probe location and artery assessed should be standardized.

Line 174 – Please also specify if you were checking the flow during the tourniquet application or how you defined the end of the tourniquet application. Other studies define the application using a set amount of windlass turns, often three; please explain how you defined the end of application in your study.

Line 174 – Please state if the examiner was blinded to the tourniquet type.

Line 176 – Please clearly explain when you stopped measuring.

Line 177 – Please reference the NRS scale and state when the measurement was performed (when the tourniquet was in place vs at the end of the application).

Line 179 – Please describe how you measured ease of use, for example, did you use a Likert scale.

Line 180 – Did you have any mechanical failures? If so, I would add this as an outcome. If not, I would specify it in the text.

Line 181- Please state if the rest periods were the same between all applications and how long they were.

Results

Please add a short paragraph where you describe your participant population, including age and weight. Please consider adding a table 1 with participant data.

Line 202 – Please keep the same order in the Results section, going from the primary outcome through the secondary outcomes (occlusion, speed, etc.). Creating different paragraphs for each outcome can help clarify your results. Please reorganize and rewrite your Results section.

Line 203 – Please separate ease of use from windlass turns. They are separate outcomes as you described in lines 179 and 180. Please clearly define how you measured ease of use.

Line 214 – If you can, please add an analysis to see if there is a correlation between the number of windlass turns and occlusion. While this is not mandatory for the paper from my standpoint, it would add value to your submission.

Table 1 – Please comment on the difference in the percentage of arterial occlusion in the lower extremity between CAT, SITCH, and DNIPRO. A 14% difference between CAT and DNIPRO is clinically very significant and could lead to an increase in preventable deaths. This difference should be underlined in the results, discussed in the discussion, and acknowledged in the limitations.

Please be cautious in interpreting the odds ratios. The confidence intervals are very wide, which likely indicates a small sample size. These findings should not be overstated.

Please indicate if you performed a sample size or power calculation.

The table should reflect the same order as the manuscript, with the primary outcome first, followed by secondary outcomes in order.

I have some concerns about the statistical analysis. Each participant performed multiple tourniquet applications (several trials per person), so the observations are not independent. However, the analysis uses chi-square and Kruskal–Wallis tests, which assume independent observations and may therefore not be appropriate for this type of repeated-measures dataset. The authors should consider using statistical methods that account for repeated measurements within the same participant (for example mixed-effects models). For occlusion success, a mixed-effects logistic regression would be more appropriate. For outcomes such as application time, pain score, and number of turns, linear mixed models or other repeated-measures approaches could be considered, depending on data distribution. Participant can be used as a random effect.

In addition, in Table 1 most comparisons are reported as statistically significant, but it is unclear which specific tourniquets differ from each other, since no pairwise comparisons are presented. Reporting direct comparisons between the devices would make the results easier to interpret.

Finally, the reported odds ratios are very large given the relatively small sample size, with wide confidence intervals. This makes them difficult to interpret and the authors should comment on this limitation.

Discussion

Line 264 – Please rephrase from “which …flow” to increase clarity.

Line 269 – Substitute completable with complete.

Line 288 – The biggest limitation is that this is a preclinical study and that the effectiveness of the device may be different in real-world use, and that your findings may not be generalizable as they were obtained under ideal conditions. Additionally, there is no data regarding complications after use, which should also be a subject of future studies.

Conclusion

Line 308 – I believe that the sentence “Our findings…. military medicine.” comes across as too strong. As valuable as your study is, it is still a preclinical study, which shows that the Ukrainian tourniquets have similar performance compared to CoTCCC tourniquets in a controlled preclinical setting on healthy human subjects. The experimental setting does not replicate realistic hemorrhage. Therefore conclusions regarding battlefield effectiveness should be interpreted cautiously. Please rephrase.

The authors address an important and relevant topic, and the effort to evaluate locally produced tourniquets is appreciated. Thank you for the strong work put into conducting this study.

Comments on the Quality of English Language

The English language is clear and the manuscript is well written. A careful proofreading for minor grammatical issues and overall flow and clarity is recommended.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

This is a timely and clinically relevant prospective crossover simulation study, particularly in the context of constrained access to CoTCCC-recommended tourniquets during ongoing armed conflict and the need to evaluate locally produced devices. The use of Doppler ultrasound to confirm arterial occlusion and the inclusion of performance outcomes such as application time, number of windlass turns, pain intensity and ease-of-use are appropriate and, in principle, very useful for both tactical and civilian prehospital practice. At the same time, several key aspects of the design and analysis need to be strengthened before firm comparative conclusions can be drawn.

Comments:

1. The single most important methodological issue is the statistical treatment of the data. Each of the 51 participants performed 16 applications (4 devices × 4 limbs), giving 816 trials that are clearly not independent observations but clustered within individuals (and arguably within limbs). The current analysis, which uses chi-square tests and Kruskal–Wallis tests as if each trial were independent, will underestimate standard errors and can lead to overly optimistic p-values and confidence intervals. I would consider it essential to re-analyse the data using an appropriate repeated-measures framework: for example, mixed-effects logistic regression (or GEE with robust standard errors) for the binary endpoint of successful arterial occlusion, with a random intercept for participant (and, ideally, limb nested within participant), and linear or generalised mixed-effects models for continuous outcomes such as time to application, number of windlass turns, and pain scores. All primary conclusions should be based on these clustered models, and p-values and effect estimates should be updated accordingly.

2. Closely linked to this, the crossover design raises concerns about learning, fatigue and carryover effects, which are not currently described or adjusted for. Participants underwent a one-hour training session and then performed repeated self-applications on all four limbs. Without explicit information on how the order of devices and limb sequence was determined, it is difficult to know to what extent improvements in speed, perceived difficulty or even occlusion success are driven by increasing familiarity and practice rather than inherent device characteristics. It is important to state clearly whether the order of devices and limbs was randomised or counterbalanced; if it was not, this should be highlighted as a major limitation. In either case, I strongly recommend including trial order (application number 1–16, and/or device order) as a covariate in the mixed models and exploring potential order-by-device interactions. A sensitivity analysis restricted to the first application of each device (or to the first limb tested) would also be very informative as a closer approximation of “real-world” first-time use.

3. The Doppler-based definition of the primary outcome is appropriate, but it needs to be described in a reproducible and operationally precise way. At present, you state that arterial occlusion was confirmed using a Butterfly iQ device and “major arteries in the limb,” but you do not specify which arteries were assessed (for example, brachial versus radial for the upper extremity; posterior tibial, dorsalis pedis or popliteal for the lower extremity), where the probe was placed, or how soon after tourniquet tightening the assessment was made. It would help to detail the standardised Doppler protocol, including the artery chosen for each limb, the exact site, whether colour Doppler or pulsed-wave flow was used, and whether occlusion had to be sustained for a minimum period to be counted as successful. Please also clarify whether the ultrasound assessor was independent of the person teaching or supervising tourniquet placement and whether they were blinded to device type; I recognise that complete blinding is challenging when devices look different, but readers need to understand how much room there is for measurement bias.

4. The way effectiveness is summarised using odds ratios with SOFTT-W as the reference group is a reasonable starting point, but in its current form it is incomplete and potentially misleading. Once clustering is handled correctly, the effect sizes may change, and it will be more informative to report model-derived adjusted probabilities of successful occlusion for each device, together with absolute risk differences and 95% confidence intervals. Given the practical nature of the question, I would encourage you to present results in terms of easily interpretable measures: for instance, “estimated probability of successful occlusion on the arm/leg,” “median application time with IQR,” and “proportion of trials with severe pain.” Pairwise comparisons between all four devices should be presented with appropriate multiplicity control (for example, Holm or FDR), rather than only relative to the SOFTT-W, so that readers can understand how DNIPRO and SITCH compare not just to one control, but also to CAT and to each other.

5. The assessment of pain is another area where the design and reporting could be strengthened. Pain scores were recorded after each application with rest periods in between, but repeated ischemic stimuli to different limbs in the same participant can alter pain perception through sensitisation or habituation, and this may interact with trial order and the participant’s expectations of each device. It is important to specify exactly when the pain NRS was recorded: immediately after locking the windlass, after the Doppler check, or after a fixed duration under occlusion. Including trial order as a covariate in the pain models and examining whether pain scores drift up or down over successive applications would be valuable. It would also make the findings more clinically actionable to define and report a threshold for “severe” pain (for example, NRS ≥ 7) and to quantify how often each device reaches this level, as well as how pain trade-offs relate to success of occlusion.

6. The generalisability of the findings is, by design, limited to trained medical personnel using tourniquets on bare skin in a calm, controlled environment with the same devices used repeatedly. That is acceptable for an initial simulation study, but it needs to be emphasised and, ideally, complemented with more realistic scenarios. In practice, tourniquets are often applied under considerable stress, in low light or adverse weather conditions, while wearing gloves, over clothing or equipment and sometimes by lay bystanders with minimal training. You mention some of these aspects in the Discussion; I would encourage you to either add a follow-up experimental component (for example, an arm where tourniquets are applied over a standardised layer of tactical/winter clothing, or under time pressure) or, at minimum, flesh out the Future Directions section with a concrete plan for such work. Including a group of novice users (or at least stratifying results by baseline tourniquet experience) would also help readers understand how device performance might translate outside a professional user population.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

The manuscript addresses a topic that is certainly interesting and likely to attract attention given the current relevance of the issue. The subject is therefore clinically relevant and of considerable practical interest for emergency medicine, and the comparison with devices recommended by international guidelines further increases the value of the study. Arterial occlusion was objectively verified using Doppler ultrasound. The study design allowed each participant to test all the devices, thereby partially reducing inter-operator variability. In addition, several operational parameters were analyzed, including occlusion success, application time, pain perception, and ease of use, which represent positive aspects of the work.

However, several limitations should be acknowledged. First, the study was conducted in a simulated environment rather than in real trauma conditions, where circumstances may differ substantially. All applications were performed repeatedly by the same participants, meaning that operators likely improved their performance over time as they became more familiar with the devices.

Furthermore, the statistical methods used, such as the chi-square test and the Kruskal–Wallis test, assume independence of observations. Given the repeated-measures design of the study, statistical models accounting for repeated observations, such as mixed-effects models, would have been more appropriate.

Participants received only a brief training session before the study, although this does not appear to be a major limitation. The number of participants is not particularly large, but it still seems adequate for an exploratory comparative study.

Secondary endpoints such as ease of use and perceived pain should also be interpreted cautiously, as they are inherently subjective and may be influenced by the methodological limitations mentioned above.

Although conducting studies under real battlefield conditions would obviously be extremely difficult and ethically problematic, this remains the main limitation of the study.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

I thank the authors for addressing most of the suggestions. I believe that the manuscript has been significantly improved. I still have three main areas of concern.

First, there is a major discrepancy in the total number of tourniquet applications reported between the original version of the manuscript (816) and the revised version (408). In the original manuscript, the authors report that all participants applied each of the four tourniquets on each limb. In the revised manuscript, they report that each participant applied the tourniquets to two limbs of their choice. This substantial reduction in observations is not explicitly addressed or explained in the revised manuscript; please clarify.

Second, the definition of a “complete” tourniquet application remains unclear and somewhat inconsistent. In one section, the authors state that the tourniquet was tightened until arterial occlusion occurred; however, they also specify that Doppler assessment of arterial flow was performed only after the tourniquet had been secured, which makes this definition unclear. Elsewhere, application time is defined as the interval from initial placement to securing of the device. Given that the number of windlass turns varies between participants, it is not clear whether a standardized endpoint was used or whether completion was left to the participant’s judgment. Please clearly define when timing started and stopped, and how a complete application was defined. If this was left to the participant’s judgment, this should be explicitly stated.

Third, while the authors appropriately revised the statistical approach and implemented mixed-effects models, the presentation of the results in Table 1 is not consistent with this analysis. The table reports descriptive statistics (percentages and medians) alongside p-values stated to be derived from mixed-effects models, without presenting regression coefficients or adjusted odds ratios, which are the typical outputs for mixed-effects models of continuous and categorical outcomes, respectively. This is misleading, as the reported p-values do not directly correspond to the descriptive statistics shown. The table should be revised to align with the statistical methods or limited to purely descriptive results.

I would see value in including an initial table with purely descriptive statistics to summarize the performance of each tourniquet before presenting the results of the mixed-effects models. I would also suggest that the authors consider involving a statistician to ensure that the analyses and their presentation are fully appropriate.

I thank the authors again for this interesting manuscript, which has the potential to provide a valuable contribution to the field if these points are adequately addressed.

Author Response

Dear Reviewer,

We would like to thank the Reviewer for the positive evaluation of our manuscript and for the constructive comments, which have helped us further improve its clarity and methodological transparency. We address each point below.

Response: We thank the Reviewer for identifying this inconsistency. The discrepancy was due to an editorial error arising from the initial study design assumptions. The original protocol considered a larger number of potential applications. However, due to organizational constraints associated with conducting the study in Kyiv during a period of repeated air raid alerts, the study procedure was shortened. Consequently, each participant applied the four tourniquet models to two selected limbs (one upper and one lower extremity), resulting in 8 applications per participant and 408 applications overall. The previously reported number (816) reflected the initial assumptions rather than the final implemented protocol. This has now been clarified in the Methods section. Importantly, all statistical analyses were performed on the correct dataset (408 applications) from the outset; the discrepancy concerned only the reported number in the manuscript text and did not affect the results or their interpretation.

Response: We thank the Reviewer for this important comment. The manuscript has been revised to clarify the definition of a complete tourniquet application and to ensure consistency throughout the text. Tourniquet application was defined as complete when the participant secured the windlass in the locking mechanism. Application time was defined as the interval from initial placement of the device on the limb to this point. Doppler ultrasound was performed only after completion of the application and was used to assess the effectiveness of arterial occlusion.

Response: We thank the Reviewer for this valuable and insightful comment. In the revised manuscript, Table 1 has been modified to present purely descriptive statistics (counts, percentages, medians, and interquartile ranges), and all p-values have been removed. The description of Table 1 in the Results section has also been revised.

I thank the authors again for this interesting manuscript, which has the potential to provide a valuable contribution to the field if these points are adequately addressed.

Response: We sincerely thank the Reviewer for the positive evaluation of our manuscript and for recognizing its potential contribution to the field.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have addressed all of my issues in a satisfactory manner.

Author Response

Dear Reviewer, We would like to thank the Reviewer for their time and for the positive evaluation of our manuscript.